paper v2.39: restructure §1-§7 into subsection hierarchy (codex proposal)

Per codex consultation, refactored §1-§7 from "section + paragraph
headers" into proper \subsection{} hierarchy. 14 subsections total.

Key decisions (from codex):
- §3 (Mode 1) and §4 (Mode 2) kept SEPARATE, not merged. Avoids
  overcommitting to the Mode 2 → Mode 1 hypothesis too early in the
  narrative.
- §5 (Intervention + Cross-arch) kept as one section with two subsections.
  Splitting would create thin sections.
- Moved old §4 ¶4 "Method-dependent severity..." into new §5.1 "Penalty
  rescue and sweep" — it's intervention-stage evidence about method
  severity after Mode 1 is alleviated, fits with rescue/sweep/cost
  evidence rather than core Mode 2 identification.

New structure:

  §1 Introduction
    1.1 Standard FA reporting
    1.2 Two failure modes and contributions
  §2 Audit: Standard Reporting Walks Back Nothing
    2.1 Audit setup and probes
    2.2 The status-quo reading fails
  §3 Failure Mode 1: Measurement Degeneracy
    3.1 Mode 1 signatures
    3.2 Terminal-LN control
  §4 Failure Mode 2: Low Intrinsic Credit-Direction Quality
    4.1 Mode 2 under valid measurement
    4.2 Functional triangulation [paper's strongest new claim]
    4.3 From Mode 2 to Mode 1? [the causal hypothesis]
  §5 Intervention and Cross-Architecture Evidence
    5.1 Penalty rescue and sweep [absorbed old §4 ¶4]
    5.2 Cost and transfer
  §6 Recommended FA Evaluation Protocol
    6.1 Validity-first screening
    6.2 Diagnostic roles and calibration
  §7 Discussion, Limits, Conclusion
    7.1 Scope and reporting recommendation
    7.2 Open questions

All \paragraph{} inline bold headers from §1-§7 were stripped since the
\subsection{} hierarchy now carries the structure. Appendix A and B
(Pitfalls Catalog) retain their \paragraph{} headers since they're
structured by pitfall/concept rather than subsection.

Page count: 20 (unchanged). 0 errors, 0 overfull boxes.

Co-Authored-By: Claude Opus 4.6 (1M context) <noreply@anthropic.com>

2 files changed, 59 insertions, 29 deletions

diff --git a/paper/main.pdf b/paper/main.pdf
index 17c578c..ba3f185 100644
--- a/paper/main.pdf
+++ b/paper/main.pdf
diff --git a/paper/main.tex b/paper/main.tex
index 4148b7e..5418c3f 100644
--- a/paper/main.tex
+++ b/paper/main.tex
@@ -33,18 +33,24 @@ Modern feedback-alignment evaluation on deep residual networks is still summariz
 \section{Introduction}
 \label{sec:intro}
 
-\paragraph{Feedback alignment and the standard reporting pair.} Backpropagation (BP) is the de facto training method for deep neural networks, but its requirement that each feedback connection carry a weight identical to the corresponding forward connection -- the weight-transport problem -- has long been considered biologically implausible \citep{lillicrap2016random,bartunov2018assessing}. \emph{Feedback alignment} (FA) \citep{lillicrap2016random} side-steps weight transport by delivering per-layer credit through fixed random feedback matrices, and its direct variant (DFA) \citep{nokland2016direct} projects the output error to every hidden layer through an independent random matrix; parallel lines include target propagation \citep{lee2015difference} and equilibrium propagation \citep{scellier2017equilibrium}. These rules are studied both as biologically-plausible alternatives to BP and as scalable, asynchronous training schemes, with recent work scaling DFA to transformer-scale architectures on language, recommendation, and view-synthesis tasks \citep{launay2020direct,akrout2019deep}. Evaluation in this line of work has converged on a two-number summary: final task accuracy, and an aggregate cosine alignment $\Gamma$ between the method's per-layer credit and the BP gradient on the trained network \citep{lillicrap2016random,nokland2016direct,akrout2019deep,launay2020direct,bartunov2018assessing}.
+\subsection{Standard FA reporting}
 
-\paragraph{The standard pair fails to validate.} On the audited 4-block $d{=}256$ ResMLP, however, Table~\ref{tab:main_audit} already shows that this accuracy-plus-$\Gamma$ pair is not a validity check: DFA reaches only $0.306 \pm 0.008$ test accuracy, below the architecture-matched frozen-blocks baseline of $0.349 \pm 0.003$, while still looking superficially comparable to other non-BP methods. Figure~\ref{fig:audit_hero} further shows that the apparent cosine evidence is concentrated at the shallowest block, with DFA at seed 42 reaching about $+0.42$ at layer 0 but approximately $-0.03$ to $0$ on layers 1--4, so the aggregate obscures where credit direction is and is not present. At the same time, the deepest BP reference norm is only about $4 \times 10^{-10}$ for DFA (three-seed mean) and a few $\times 10^{-9}$ for State Bridge and Credit Bridge, all below the $10^{-8}$ clamp used by \texttt{F.cosine\_similarity}, whereas BP remains around $4 \times 10^{-4}$, so the reported deep cosine is partly computed against a numerical-floor reference rather than an informative gradient direction (Figure~\ref{fig:audit_hero}; Table~\ref{tab:main_audit}). Those numbers can be useful, but only if the measurement regime itself is valid.
+Backpropagation (BP) is the de facto training method for deep neural networks, but its requirement that each feedback connection carry a weight identical to the corresponding forward connection -- the weight-transport problem -- has long been considered biologically implausible \citep{lillicrap2016random,bartunov2018assessing}. \emph{Feedback alignment} (FA) \citep{lillicrap2016random} side-steps weight transport by delivering per-layer credit through fixed random feedback matrices, and its direct variant (DFA) \citep{nokland2016direct} projects the output error to every hidden layer through an independent random matrix; parallel lines include target propagation \citep{lee2015difference} and equilibrium propagation \citep{scellier2017equilibrium}. These rules are studied both as biologically-plausible alternatives to BP and as scalable, asynchronous training schemes, with recent work scaling DFA to transformer-scale architectures on language, recommendation, and view-synthesis tasks \citep{launay2020direct,akrout2019deep}. Evaluation in this line of work has converged on a two-number summary: final task accuracy, and an aggregate cosine alignment $\Gamma$ between the method's per-layer credit and the BP gradient on the trained network \citep{lillicrap2016random,nokland2016direct,akrout2019deep,launay2020direct,bartunov2018assessing}.
 
-\paragraph{Two failure modes and their separability.} Our audit shows that modern residual vision models can make these two quantities look informative while failing to answer the question they are taken to answer. Figure~\ref{fig:audit_hero} shows the first failure mode, which we call \emph{Mode 1: measurement degeneracy}, where residual-stream growth drives the deepest hidden state to about $\|h_L\| \sim 10^8$ under DFA/SB/CB while the corresponding BP reference collapses to $\|g_L\| \sim 4 \times 10^{-10}$ for DFA (three-seed mean), so the deep-layer cosine is measured against a clamp-dominated floor rather than a meaningful target direction. The same figure also shows the second failure mode, \emph{Mode 2: low intrinsic credit-direction quality}, because even after comparing against the stronger frozen-blocks baseline ($0.349 \pm 0.003$) and looking layer-by-layer, DFA's deep blocks remain essentially null while only layer 0 is visibly positive. Intervention sharpens both modes. Adding a per-block residual penalty $\lambda \|f_l(h_l)\|^2$ to DFA at $\lambda{=}10^{-2}$ contains $\|h_L\|$ to about $4\times 10^4$ and lifts the deep BP reference to about $10^{-6}$, but DFA's rescued deep cosine is only about $+0.15$; State Bridge under the same intervention reaches a three-seed deep cosine of $+0.32$ and, unlike DFA, exceeds the frozen-blocks baseline by $+10$ points in final accuracy; Credit Bridge reaches a deep cosine near $+0.68$ yet matches only the DFA accuracy, so Mode~2 has method-dependent severity and deep cosine is not a sufficient predictor of final accuracy across methods. At the same time, at $\lambda{=}10^{-4}$ Mode~1 is alleviated while the DFA deep cosine still stays near zero, and at vanilla DFA epoch 1 the reference is already meaningful at about $6 \times 10^{-7}$ but the deep cosine is still $-0.008 \pm 0.016$ across three seeds. The failure is therefore neither unitary nor uniform: Mode~1 and Mode~2 are observationally separable, and within the audited fixed-feedback family, the severity of each mode varies by method.
+On the audited 4-block $d{=}256$ ResMLP, however, Table~\ref{tab:main_audit} already shows that this accuracy-plus-$\Gamma$ pair is not a validity check: DFA reaches only $0.306 \pm 0.008$ test accuracy, below the architecture-matched frozen-blocks baseline of $0.349 \pm 0.003$, while still looking superficially comparable to other non-BP methods. Figure~\ref{fig:audit_hero} further shows that the apparent cosine evidence is concentrated at the shallowest block, with DFA at seed 42 reaching about $+0.42$ at layer 0 but approximately $-0.03$ to $0$ on layers 1--4, so the aggregate obscures where credit direction is and is not present. At the same time, the deepest BP reference norm is only about $4 \times 10^{-10}$ for DFA (three-seed mean) and a few $\times 10^{-9}$ for State Bridge and Credit Bridge, all below the $10^{-8}$ clamp used by \texttt{F.cosine\_similarity}, whereas BP remains around $4 \times 10^{-4}$, so the reported deep cosine is partly computed against a numerical-floor reference rather than an informative gradient direction (Figure~\ref{fig:audit_hero}; Table~\ref{tab:main_audit}). Those numbers can be useful, but only if the measurement regime itself is valid.
 
-\paragraph{Contribution: a methodology paper, not a new FA variant.} Accordingly, this paper does not introduce a new FA variant or a new benchmark. Of the five methods we audit, BP, EP, and DFA are established baselines from the published literature; the remaining two, which we call \emph{State Bridge} and \emph{Credit Bridge}, are diagnostic probes we construct in this paper to directly learn the two targets that different strands of the BP-free literature argue should produce good per-layer credit (formal definitions and citations in Section~\ref{sec:audit}). Instead, Table~\ref{tab:main_audit} and Figure~\ref{fig:audit_hero} use a standard five-method CIFAR-10 audit to show that status-quo reporting would treat BP, EP, DFA, State Bridge, and Credit Bridge as the same kind of evidence-bearing object even though only BP and EP remain trustworthy under matched diagnostic checks. This makes the contribution methodological in the sense of \citet{jordan2020evaluating}, \citet{obray2022evaluation}, and \citet{paleka2026pitfalls}: the central question is not whether one more FA variant can post a headline number, but whether the reporting pipeline distinguishes meaningful credit-direction evidence from numerical-floor artifacts and from shallow-only learning. The protocol therefore starts from per-layer diagnostics and a frozen-blocks baseline before reading any aggregate cosine or final accuracy as evidence about deep credit assignment. We first show the walk-back on a standard audit, then isolate the two failure modes, and finally state the reporting protocol that future FA papers should satisfy.
+\subsection{Two failure modes and contributions}
+
+Our audit shows that modern residual vision models can make these two quantities look informative while failing to answer the question they are taken to answer. Figure~\ref{fig:audit_hero} shows the first failure mode, which we call \emph{Mode 1: measurement degeneracy}, where residual-stream growth drives the deepest hidden state to about $\|h_L\| \sim 10^8$ under DFA/SB/CB while the corresponding BP reference collapses to $\|g_L\| \sim 4 \times 10^{-10}$ for DFA (three-seed mean), so the deep-layer cosine is measured against a clamp-dominated floor rather than a meaningful target direction. The same figure also shows the second failure mode, \emph{Mode 2: low intrinsic credit-direction quality}, because even after comparing against the stronger frozen-blocks baseline ($0.349 \pm 0.003$) and looking layer-by-layer, DFA's deep blocks remain essentially null while only layer 0 is visibly positive. Intervention sharpens both modes. Adding a per-block residual penalty $\lambda \|f_l(h_l)\|^2$ to DFA at $\lambda{=}10^{-2}$ contains $\|h_L\|$ to about $4\times 10^4$ and lifts the deep BP reference to about $10^{-6}$, but DFA's rescued deep cosine is only about $+0.15$; State Bridge under the same intervention reaches a three-seed deep cosine of $+0.32$ and, unlike DFA, exceeds the frozen-blocks baseline by $+10$ points in final accuracy; Credit Bridge reaches a deep cosine near $+0.68$ yet matches only the DFA accuracy, so Mode~2 has method-dependent severity and deep cosine is not a sufficient predictor of final accuracy across methods. At the same time, at $\lambda{=}10^{-4}$ Mode~1 is alleviated while the DFA deep cosine still stays near zero, and at vanilla DFA epoch 1 the reference is already meaningful at about $6 \times 10^{-7}$ but the deep cosine is still $-0.008 \pm 0.016$ across three seeds. The failure is therefore neither unitary nor uniform: Mode~1 and Mode~2 are observationally separable, and within the audited fixed-feedback family, the severity of each mode varies by method.
+
+Accordingly, this paper does not introduce a new FA variant or a new benchmark. Of the five methods we audit, BP, EP, and DFA are established baselines from the published literature; the remaining two, which we call \emph{State Bridge} and \emph{Credit Bridge}, are diagnostic probes we construct in this paper to directly learn the two targets that different strands of the BP-free literature argue should produce good per-layer credit (formal definitions and citations in Section~\ref{sec:audit}). Instead, Table~\ref{tab:main_audit} and Figure~\ref{fig:audit_hero} use a standard five-method CIFAR-10 audit to show that status-quo reporting would treat BP, EP, DFA, State Bridge, and Credit Bridge as the same kind of evidence-bearing object even though only BP and EP remain trustworthy under matched diagnostic checks. This makes the contribution methodological in the sense of \citet{jordan2020evaluating}, \citet{obray2022evaluation}, and \citet{paleka2026pitfalls}: the central question is not whether one more FA variant can post a headline number, but whether the reporting pipeline distinguishes meaningful credit-direction evidence from numerical-floor artifacts and from shallow-only learning. The protocol therefore starts from per-layer diagnostics and a frozen-blocks baseline before reading any aggregate cosine or final accuracy as evidence about deep credit assignment. We first show the walk-back on a standard audit, then isolate the two failure modes, and finally state the reporting protocol that future FA papers should satisfy.
 
 \section{Audit: Standard Reporting Walks Back Nothing}
 \label{sec:audit}
 
-\paragraph{Setup: 5-method audit on a 4-block pre-LayerNorm ResMLP.} Table~\ref{tab:main_audit} fixes the canonical audit to a 4-block pre-LayerNorm ResMLP with width $d{=}256$ on CIFAR-10, trained for 100 epochs with AdamW (learning rate $10^{-3}$, weight decay $0.01$), a cosine schedule, batch size $128$, and three seeds (42, 123, 456); all five methods are read against the identical architecture, optimizer, schedule, and training budget without method-specific tuning, and Figure~\ref{fig:audit_hero} summarizes the corresponding per-block growth, deepest-layer BP reference norm, cross-batch stability, and frozen-baseline comparison.
+\subsection{Audit setup and probes}
+
+Table~\ref{tab:main_audit} fixes the canonical audit to a 4-block pre-LayerNorm ResMLP with width $d{=}256$ on CIFAR-10, trained for 100 epochs with AdamW (learning rate $10^{-3}$, weight decay $0.01$), a cosine schedule, batch size $128$, and three seeds (42, 123, 456); all five methods are read against the identical architecture, optimizer, schedule, and training budget without method-specific tuning, and Figure~\ref{fig:audit_hero} summarizes the corresponding per-block growth, deepest-layer BP reference norm, cross-batch stability, and frozen-baseline comparison.
 
 \begin{table}[t]
 \centering
@@ -65,13 +71,15 @@ Credit Bridge & $0.289 \pm 0.031$ & $0.07$        & trustworthy & walked back \\
 \end{tabular}}
 \end{table}
 
-\paragraph{State Bridge and Credit Bridge: diagnostic probes constructed for this paper.} Two rows in Table~\ref{tab:main_audit}, \emph{State Bridge} (SB) and \emph{Credit Bridge} (CB), are diagnostic probes we construct in this paper, not prior FA variants. Each directly learns a target that a different strand of the BP-free literature argues should produce good per-layer credit, and each uses the same block local loss $-\langle f_l(h_l),\, a_l\rangle$ as DFA but with a different $a_l$. SB instantiates the target-propagation view that accurate prediction of a downstream hidden state yields a usable credit signal \citep{bengio2014autoencoders,lee2015difference}: an auxiliary $G_\psi(h_l, t_l, s)$ is fit by MSE to predict $h_L$ from $(h_l, t_l{=}l/L, s{=}e_T)$, and $a_l^{\mathrm{SB}} = \nabla_{h_l}\,\mathrm{CE}(W_{\mathrm{out}}\,\mathrm{LN}(G_\psi(h_l, t_l, s)), y)$. CB instantiates the synthetic-gradient view that a learned value network, if its input-gradient approximates the BP gradient, can stand in for it \citep{jaderberg2017decoupled}: $V_\phi(h_l, t_l, s)$ is fit via a bridge residual against an EMA target, and $a_l^{\mathrm{CB}} = \nabla_{h_l} V_\phi(h_l, t_l, s)$. Both auxiliaries are trained on detached hidden states. We use SB and CB as controls that populate different points in the (angular agreement with BP, functional usefulness) plane; that is what makes the cross-method cosine-versus-accuracy dissociation in Section~\ref{sec:mode2} visible.
+Two rows in Table~\ref{tab:main_audit}, \emph{State Bridge} (SB) and \emph{Credit Bridge} (CB), are diagnostic probes we construct in this paper, not prior FA variants. Each directly learns a target that a different strand of the BP-free literature argues should produce good per-layer credit, and each uses the same block local loss $-\langle f_l(h_l),\, a_l\rangle$ as DFA but with a different $a_l$. SB instantiates the target-propagation view that accurate prediction of a downstream hidden state yields a usable credit signal \citep{bengio2014autoencoders,lee2015difference}: an auxiliary $G_\psi(h_l, t_l, s)$ is fit by MSE to predict $h_L$ from $(h_l, t_l{=}l/L, s{=}e_T)$, and $a_l^{\mathrm{SB}} = \nabla_{h_l}\,\mathrm{CE}(W_{\mathrm{out}}\,\mathrm{LN}(G_\psi(h_l, t_l, s)), y)$. CB instantiates the synthetic-gradient view that a learned value network, if its input-gradient approximates the BP gradient, can stand in for it \citep{jaderberg2017decoupled}: $V_\phi(h_l, t_l, s)$ is fit via a bridge residual against an EMA target, and $a_l^{\mathrm{CB}} = \nabla_{h_l} V_\phi(h_l, t_l, s)$. Both auxiliaries are trained on detached hidden states. We use SB and CB as controls that populate different points in the (angular agreement with BP, functional usefulness) plane; that is what makes the cross-method cosine-versus-accuracy dissociation in Section~\ref{sec:mode2} visible.
+
+\subsection{The status-quo reading fails}
 
-\paragraph{Status-quo reading: every method looks acceptable.} By the field's usual criteria, the non-BP methods appear to train to nontrivial accuracy and report nonzero alignment. In Table~\ref{tab:main_audit}, DFA reaches $0.306 \pm 0.008$ test accuracy with headline $\Gamma{=}0.10$, State Bridge reaches $0.205 \pm 0.039$ with $\Gamma{=}0.005$, and Credit Bridge reaches $0.289 \pm 0.031$ with $\Gamma{=}0.07$; none of these rows looks like an obvious invalidation if one is reading the usual pair of final accuracy and aggregate alignment in the style of prior FA reporting \citep{lillicrap2016random,nokland2016direct,akrout2019deep,launay2020direct}. Even the absolute scale does not itself force a walk-back, because all three methods are plainly above chance and all three report positive headline alignment rather than a visibly broken or undefined quantity. That reading is exactly what the rest of the paper overturns.
+By the field's usual criteria, the non-BP methods appear to train to nontrivial accuracy and report nonzero alignment. In Table~\ref{tab:main_audit}, DFA reaches $0.306 \pm 0.008$ test accuracy with headline $\Gamma{=}0.10$, State Bridge reaches $0.205 \pm 0.039$ with $\Gamma{=}0.005$, and Credit Bridge reaches $0.289 \pm 0.031$ with $\Gamma{=}0.07$; none of these rows looks like an obvious invalidation if one is reading the usual pair of final accuracy and aggregate alignment in the style of prior FA reporting \citep{lillicrap2016random,nokland2016direct,akrout2019deep,launay2020direct}. Even the absolute scale does not itself force a walk-back, because all three methods are plainly above chance and all three report positive headline alignment rather than a visibly broken or undefined quantity. That reading is exactly what the rest of the paper overturns.
 
-\paragraph{EP as the internal control: low accuracy without invalid measurement.} Low accuracy by itself is not the pathology. Equilibrium Propagation (EP), a contrastive energy-based alternative to BP that updates weights from the difference between a free-phase and a nudged-phase hidden trajectory, is the key internal comparison in Table~\ref{tab:main_audit} and Figure~\ref{fig:audit_hero}: it achieves only $0.316 \pm 0.037$ accuracy and a very small headline $\Gamma{=}0.008$, yet its three-seed mean max-per-block growth is only $6.6\times$ (highest single-seed value $11.0\times$), its deepest BP reference norm remains around $1.3\times 10^{-4}$ rather than collapsing to the numerical floor, and its cross-batch direction-stability score is $0.02$ rather than the much higher drift-dominated values seen for DFA-family methods. At the same time, EP is not a positive result for depth usage in the stronger sense, because its trainable-model accuracy is still $3.3$ percentage points below the frozen-blocks baseline of $0.349 \pm 0.003$. The distinction matters because it separates underperformance from invalid evaluation.
+Low accuracy by itself is not the pathology. Equilibrium Propagation (EP), a contrastive energy-based alternative to BP that updates weights from the difference between a free-phase and a nudged-phase hidden trajectory, is the key internal comparison in Table~\ref{tab:main_audit} and Figure~\ref{fig:audit_hero}: it achieves only $0.316 \pm 0.037$ accuracy and a very small headline $\Gamma{=}0.008$, yet its three-seed mean max-per-block growth is only $6.6\times$ (highest single-seed value $11.0\times$), its deepest BP reference norm remains around $1.3\times 10^{-4}$ rather than collapsing to the numerical floor, and its cross-batch direction-stability score is $0.02$ rather than the much higher drift-dominated values seen for DFA-family methods. At the same time, EP is not a positive result for depth usage in the stronger sense, because its trainable-model accuracy is still $3.3$ percentage points below the frozen-blocks baseline of $0.349 \pm 0.003$. The distinction matters because it separates underperformance from invalid evaluation.
 
-\paragraph{Frozen-blocks baseline overturns the status-quo reading.} When we compare each method to a frozen-blocks baseline matched to the same architecture, the headline interpretation changes immediately. The frozen-blocks model, which trains only the embedding, LayerNorm, and head while holding the residual blocks fixed, reaches $0.349 \pm 0.003$ across the same three seeds; against that baseline, BP is higher by $26.6$ points, but DFA is lower by $4.3$ points, State Bridge by $14.4$ points, Credit Bridge by $6.0$ points, and even EP by $3.3$ points. Figure~\ref{fig:audit_hero} shows that this accuracy comparison lines up with the diagnostic split: DFA, State Bridge, and Credit Bridge also combine extreme per-block growth (three-seed mean max ratios $\sim\!1.9\times 10^3$, $\sim\!1.6\times 10^4$, and $\sim\!1.2\times 10^3$ respectively), deepest-layer BP norms around $10^{-9}$, and high cross-batch instability ($0.16$, $0.53$, and $0.37$), so their deep blocks are at best passengers and in practice often harmful. This establishes the audit question the rest of the paper must answer: why do the standard signals fail so badly?
+When we compare each method to a frozen-blocks baseline matched to the same architecture, the headline interpretation changes immediately. The frozen-blocks model, which trains only the embedding, LayerNorm, and head while holding the residual blocks fixed, reaches $0.349 \pm 0.003$ across the same three seeds; against that baseline, BP is higher by $26.6$ points, but DFA is lower by $4.3$ points, State Bridge by $14.4$ points, Credit Bridge by $6.0$ points, and even EP by $3.3$ points. Figure~\ref{fig:audit_hero} shows that this accuracy comparison lines up with the diagnostic split: DFA, State Bridge, and Credit Bridge also combine extreme per-block growth (three-seed mean max ratios $\sim\!1.9\times 10^3$, $\sim\!1.6\times 10^4$, and $\sim\!1.2\times 10^3$ respectively), deepest-layer BP norms around $10^{-9}$, and high cross-batch instability ($0.16$, $0.53$, and $0.37$), so their deep blocks are at best passengers and in practice often harmful. This establishes the audit question the rest of the paper must answer: why do the standard signals fail so badly?
 
 \begin{figure}[t]
 \centering
@@ -83,30 +91,38 @@ Credit Bridge & $0.289 \pm 0.031$ & $0.07$        & trustworthy & walked back \\
 \section{Failure Mode 1: Measurement Degeneracy}
 \label{sec:mode1}
 
-\paragraph{The two parts of Mode~1.} Mode~1 has two parts. The activation-growth part~(a) is a scale pathology of fixed-feedback local-credit objectives without an effective scale-control term: for block $l$, DFA, State Bridge, and Credit Bridge each update $f_l$ by maximizing a local objective of the form $\langle f_l(h_l),\, a_l\rangle$, where the per-layer credit vector $a_l$ is the method-specific projection of the output error (for DFA, $a_l = B_l^\top e_T$ with a fixed random $B_l$; for State Bridge, $a_l$ is the gradient of a cross-entropy loss measured through a learned state predictor $G_\psi(h_l,t_l,s)$ that estimates $h_L$; for Credit Bridge, $a_l$ is the gradient of a learned value network $V(h_l,t_l,s)$). None of these three local losses contains a penalty on $\|f_l(h_l)\|$, so any direction in which a larger block output improves inner-product alignment with the method's fixed or learned credit target is rewarded; in a pre-LN residual stack, larger block outputs directly increase residual-stream scale, and terminal LayerNorm at the output removes task-loss sensitivity to that scale, so the architecture supplies no global restraint on the local growth incentive. The gradient-floor part~(b) follows from the LayerNorm Jacobian. For $y = \mathrm{LN}(h) = (h - \mu(h))/\sigma(h)$ with $\sigma(h) = \big(\tfrac{1}{d}\sum_i (h_i - \mu(h))^2\big)^{1/2}$ proportional to $\|h\|/\sqrt{d}$, the spectral norm of $\partial y/\partial h$ is $\Theta(1/\sigma(h))$, so back-propagating through terminal LayerNorm scales the deepest hidden BP gradient as $\|g_L\| = \Theta(1/\|h_L\|)$, and the same residual-stream inflation that drives diagnostic~(a) drives a proportional collapse of the diagnostic~(b) reference. Empirically, on the audited 4-block pre-LayerNorm ResMLP ($d{=}256$, CIFAR-10, 100 epochs, 3 seeds), DFA training drives the three-seed mean $\|h_L\|$ from about $9$ at initialization to about $5\times 10^8$ by epoch 100 and $\|g_L\|$ from about $9.8\times 10^{-4}$ to about $4\times 10^{-10}$, while the reported deep cosine remains defined only because \texttt{F.cosine\_similarity} clamps the denominator at $\varepsilon{=}10^{-8}$ (Table~\ref{tab:main_audit}; Figure~\ref{fig:audit_hero}). At that endpoint the reference norm is about $25\times$ below the clamp, so the quantity being reported is effectively $(a\cdot b)/(\|a\|\max(\|b\|,10^{-8}))$ rather than a comparison to a meaningful BP direction.
+\subsection{Mode~1 signatures}
 
-\paragraph{Falsification chain: four alternative attributions.} We tested this mechanism story against four natural alternative attributions, all of which it survives. \emph{Not residual-skip-driven:} with terminal LN kept and the additive skip removed ($h_{l+1}{=}F_l(h_l)$), DFA still converges across three seeds to mean $\|h_L\|{\approx}8.2{\times}10^{7}$ and mean $\|g_L\|{\approx}1.9{\times}10^{-10}$ at $100$ epochs, both at the diagnostic floor (Appendix~\ref{app:no_residual}). \emph{Not task-signal-driven:} under i.i.d.\ random class targets per minibatch, DFA still reaches $\|h_L\|{\approx}1.67{\times}10^{8}$ and $\|g_L\|{\approx}8{\times}10^{-12}$ while accuracy stays at chance (Appendix~\ref{app:random_targets}). \emph{Not DFA-specific:} the same random-target ablation drives $\|h_L\|$ to $6.2{\times}10^{3}$ for SB and $2.0{\times}10^{4}$ for CB in three epochs, so all three audited fixed-feedback methods exhibit data-agnostic activation growth. \emph{Not shared by EP:} under the same protocol, EP keeps $\|h_L\|{\approx}586$ at five epochs, $25\times$ smaller than DFA's three-epoch value, confirming that the random-target assay separates the explosion-prone fixed-feedback class from EP's energy-based objective.
+Mode~1 has two parts. The activation-growth part~(a) is a scale pathology of fixed-feedback local-credit objectives without an effective scale-control term: for block $l$, DFA, State Bridge, and Credit Bridge each update $f_l$ by maximizing a local objective of the form $\langle f_l(h_l),\, a_l\rangle$, where the per-layer credit vector $a_l$ is the method-specific projection of the output error (for DFA, $a_l = B_l^\top e_T$ with a fixed random $B_l$; for State Bridge, $a_l$ is the gradient of a cross-entropy loss measured through a learned state predictor $G_\psi(h_l,t_l,s)$ that estimates $h_L$; for Credit Bridge, $a_l$ is the gradient of a learned value network $V(h_l,t_l,s)$). None of these three local losses contains a penalty on $\|f_l(h_l)\|$, so any direction in which a larger block output improves inner-product alignment with the method's fixed or learned credit target is rewarded; in a pre-LN residual stack, larger block outputs directly increase residual-stream scale, and terminal LayerNorm at the output removes task-loss sensitivity to that scale, so the architecture supplies no global restraint on the local growth incentive. The gradient-floor part~(b) follows from the LayerNorm Jacobian. For $y = \mathrm{LN}(h) = (h - \mu(h))/\sigma(h)$ with $\sigma(h) = \big(\tfrac{1}{d}\sum_i (h_i - \mu(h))^2\big)^{1/2}$ proportional to $\|h\|/\sqrt{d}$, the spectral norm of $\partial y/\partial h$ is $\Theta(1/\sigma(h))$, so back-propagating through terminal LayerNorm scales the deepest hidden BP gradient as $\|g_L\| = \Theta(1/\|h_L\|)$, and the same residual-stream inflation that drives diagnostic~(a) drives a proportional collapse of the diagnostic~(b) reference. Empirically, on the audited 4-block pre-LayerNorm ResMLP ($d{=}256$, CIFAR-10, 100 epochs, 3 seeds), DFA training drives the three-seed mean $\|h_L\|$ from about $9$ at initialization to about $5\times 10^8$ by epoch 100 and $\|g_L\|$ from about $9.8\times 10^{-4}$ to about $4\times 10^{-10}$, while the reported deep cosine remains defined only because \texttt{F.cosine\_similarity} clamps the denominator at $\varepsilon{=}10^{-8}$ (Table~\ref{tab:main_audit}; Figure~\ref{fig:audit_hero}). At that endpoint the reference norm is about $25\times$ below the clamp, so the quantity being reported is effectively $(a\cdot b)/(\|a\|\max(\|b\|,10^{-8}))$ rather than a comparison to a meaningful BP direction.
 
-\paragraph{Causal control: removing terminal LayerNorm on the same backbone.} The matched same-backbone causal control for diagnostic~(b) is removing terminal LayerNorm. On the same ResMLP-d256 with the residual skip intact, $100$ epochs of DFA, three seeds, the residual stream still inflates to $\|h_L\|\!\approx\!1.21\times 10^7$, but the deepest hidden-layer BP gradient remains at $\|g_L\|\!\approx\!7.2\times 10^{-4}$ (four orders of magnitude above the diagnostic~(b) floor), and the final test accuracy is $0.327\pm 0.012$, statistically indistinguishable from vanilla DFA's $0.306\pm 0.006$ on the same backbone with terminal LayerNorm intact. Removing terminal LayerNorm therefore preserves Mode~1~(a) but cleanly eliminates Mode~1~(b) on the same architecture, while leaving final task accuracy essentially unchanged. Combined with the broader cross-architecture pattern (the no-terminal-LN ResMLP-d256 ablation and the BatchNorm CNN, which lack terminal LayerNorm, never trigger diagnostic~(b); ViT-Mini with a terminal LN does, by epochs 2--3 (Figure~\ref{fig:temporal_cross_arch})), terminal LayerNorm is necessary for Mode~1~(b) in the audited residual ResMLP and ViT-Mini setting. The collapse is also not a late-epoch curiosity: $\|g_L\|$ drops from $9.8\times 10^{-4}$ at epoch~0 to $5.8\times 10^{-8}$ by epoch~4 in the three-seed temporal replay (per seed: $6.8$, $6.4$, $4.1\times 10^{-8}$), so the protocol fires within the first $11$ epochs of a $100$-epoch run and is actionable as an early-stop criterion rather than a post hoc explanation. Once measurement degeneracy is identified, the next question is whether poor deep credit remains even before collapse.
+We tested this mechanism story against four natural alternative attributions, all of which it survives. \emph{Not residual-skip-driven:} with terminal LN kept and the additive skip removed ($h_{l+1}{=}F_l(h_l)$), DFA still converges across three seeds to mean $\|h_L\|{\approx}8.2{\times}10^{7}$ and mean $\|g_L\|{\approx}1.9{\times}10^{-10}$ at $100$ epochs, both at the diagnostic floor (Appendix~\ref{app:no_residual}). \emph{Not task-signal-driven:} under i.i.d.\ random class targets per minibatch, DFA still reaches $\|h_L\|{\approx}1.67{\times}10^{8}$ and $\|g_L\|{\approx}8{\times}10^{-12}$ while accuracy stays at chance (Appendix~\ref{app:random_targets}). \emph{Not DFA-specific:} the same random-target ablation drives $\|h_L\|$ to $6.2{\times}10^{3}$ for SB and $2.0{\times}10^{4}$ for CB in three epochs, so all three audited fixed-feedback methods exhibit data-agnostic activation growth. \emph{Not shared by EP:} under the same protocol, EP keeps $\|h_L\|{\approx}586$ at five epochs, $25\times$ smaller than DFA's three-epoch value, confirming that the random-target assay separates the explosion-prone fixed-feedback class from EP's energy-based objective.
+
+\subsection{Terminal-LN control}
+
+The matched same-backbone causal control for diagnostic~(b) is removing terminal LayerNorm. On the same ResMLP-d256 with the residual skip intact, $100$ epochs of DFA, three seeds, the residual stream still inflates to $\|h_L\|\!\approx\!1.21\times 10^7$, but the deepest hidden-layer BP gradient remains at $\|g_L\|\!\approx\!7.2\times 10^{-4}$ (four orders of magnitude above the diagnostic~(b) floor), and the final test accuracy is $0.327\pm 0.012$, statistically indistinguishable from vanilla DFA's $0.306\pm 0.006$ on the same backbone with terminal LayerNorm intact. Removing terminal LayerNorm therefore preserves Mode~1~(a) but cleanly eliminates Mode~1~(b) on the same architecture, while leaving final task accuracy essentially unchanged. Combined with the broader cross-architecture pattern (the no-terminal-LN ResMLP-d256 ablation and the BatchNorm CNN, which lack terminal LayerNorm, never trigger diagnostic~(b); ViT-Mini with a terminal LN does, by epochs 2--3 (Figure~\ref{fig:temporal_cross_arch})), terminal LayerNorm is necessary for Mode~1~(b) in the audited residual ResMLP and ViT-Mini setting. The collapse is also not a late-epoch curiosity: $\|g_L\|$ drops from $9.8\times 10^{-4}$ at epoch~0 to $5.8\times 10^{-8}$ by epoch~4 in the three-seed temporal replay (per seed: $6.8$, $6.4$, $4.1\times 10^{-8}$), so the protocol fires within the first $11$ epochs of a $100$-epoch run and is actionable as an early-stop criterion rather than a post hoc explanation. Once measurement degeneracy is identified, the next question is whether poor deep credit remains even before collapse.
 
 \section{Failure Mode 2: Low Intrinsic Credit-Direction Quality}
 \label{sec:mode2}
 
-\paragraph{Mode~2 is present even when measurement is meaningful.} The second failure mode appears even in the meaningful-measurement regime. At the earliest vanilla DFA checkpoints on ResMLP, the hidden backpropagated gradient at the first deep block remains above the numerical floor: at epoch 1, $\|g_2\|$ is $6.8\times 10^{-7}$, $6.6\times 10^{-7}$, and $3.8\times 10^{-7}$ across the three seeds, all above the $10^{-7}$ threshold used to distinguish measurable from collapsed gradients. Yet the corresponding deep-layer cosine values are already essentially null: across layers $1$--$4$, all seed-level measurements at epoch 1 lie in $[-0.04,+0.02]$, with a three-seed mean of $-0.008 \pm 0.016$, and by epoch 2 the deep mean is still only $-0.018 \pm 0.017$ (Table~\ref{tab:mode_validation}). This is the observational pattern predicted by low credit-direction quality rather than mere disappearance of signal: the gradient is still present enough to measure, but the directions delivered to the deep network carry little agreement with backpropagation, consistent with prior concerns that alternative feedback rules can fail by supplying poor credit assignments even before full collapse \citep{bartunov2018assessing,moskovitz2018feedback,crafton2019backpropagation,refinetti2023aligning}. This rules out the simplest objection that the deep-layer null result is merely a byproduct of collapse.
+\subsection{Mode~2 under valid measurement}
+
+The second failure mode appears even in the meaningful-measurement regime. At the earliest vanilla DFA checkpoints on ResMLP, the hidden backpropagated gradient at the first deep block remains above the numerical floor: at epoch 1, $\|g_2\|$ is $6.8\times 10^{-7}$, $6.6\times 10^{-7}$, and $3.8\times 10^{-7}$ across the three seeds, all above the $10^{-7}$ threshold used to distinguish measurable from collapsed gradients. Yet the corresponding deep-layer cosine values are already essentially null: across layers $1$--$4$, all seed-level measurements at epoch 1 lie in $[-0.04,+0.02]$, with a three-seed mean of $-0.008 \pm 0.016$, and by epoch 2 the deep mean is still only $-0.018 \pm 0.017$ (Table~\ref{tab:mode_validation}). This is the observational pattern predicted by low credit-direction quality rather than mere disappearance of signal: the gradient is still present enough to measure, but the directions delivered to the deep network carry little agreement with backpropagation, consistent with prior concerns that alternative feedback rules can fail by supplying poor credit assignments even before full collapse \citep{bartunov2018assessing,moskovitz2018feedback,crafton2019backpropagation,refinetti2023aligning}. This rules out the simplest objection that the deep-layer null result is merely a byproduct of collapse.
+
+A second metric with different numerical failure modes tells the same story. Cosine measures directional agreement with the BP gradient, whereas the per-layer perturbation correlation $\rho_l$ measures whether the proposed credit predicts the actual loss response: for $M{=}32$ unit-norm random directions $v_m$ and step $\varepsilon{=}10^{-3}$, $\rho_l \;{=}\; \mathrm{Pearson}_m\!\left(\langle a_l,\, \varepsilon v_m\rangle,\;\, \ell(h_l + \varepsilon v_m) - \ell(h_l)\right)$, evaluated per sample on a fixed eval batch and then averaged. Cosine and $\rho$ have different failure modes, especially with respect to normalization and small-denominator effects. In our controls, $\rho$ behaves as expected, with a Taylor-ceiling positive control near $+0.997$ and a random-vector negative control near $+0.006$ (Figure~\ref{fig:penalty_rescue}, Table~\ref{tab:mode_validation}). On vanilla DFA, deep $\rho$ is likewise null: for the early checkpoints where the gradients remain measurable, the deep average is $-0.003 \pm 0.004$ across seeds and epochs, and in a floor-level checkpoint it is $+0.002$, again indistinguishable from noise. The agreement between cosine and $\rho$ therefore rules out the interpretation that the null deep result is an artifact of cosine's $\varepsilon$-clamp or vector normalization. The deep blocks are not just hard to measure; they are receiving weakly useful directions.
 
-\paragraph{A second metric with different failure modes agrees.} A second metric with different numerical failure modes tells the same story. Cosine measures directional agreement with the BP gradient, whereas the per-layer perturbation correlation $\rho_l$ measures whether the proposed credit predicts the actual loss response: for $M{=}32$ unit-norm random directions $v_m$ and step $\varepsilon{=}10^{-3}$, $\rho_l \;{=}\; \mathrm{Pearson}_m\!\left(\langle a_l,\, \varepsilon v_m\rangle,\;\, \ell(h_l + \varepsilon v_m) - \ell(h_l)\right)$, evaluated per sample on a fixed eval batch and then averaged. Cosine and $\rho$ have different failure modes, especially with respect to normalization and small-denominator effects. In our controls, $\rho$ behaves as expected, with a Taylor-ceiling positive control near $+0.997$ and a random-vector negative control near $+0.006$ (Figure~\ref{fig:penalty_rescue}, Table~\ref{tab:mode_validation}). On vanilla DFA, deep $\rho$ is likewise null: for the early checkpoints where the gradients remain measurable, the deep average is $-0.003 \pm 0.004$ across seeds and epochs, and in a floor-level checkpoint it is $+0.002$, again indistinguishable from noise. The agreement between cosine and $\rho$ therefore rules out the interpretation that the null deep result is an artifact of cosine's $\varepsilon$-clamp or vector normalization. The deep blocks are not just hard to measure; they are receiving weakly useful directions.
+Per-layer reporting is therefore not cosmetic. In ResMLP under vanilla DFA, the headline aggregate alignment $\Gamma \approx 0.07$--$0.10$ can look mildly positive only because layer $0$ remains strongly aligned while the deep network is not: at the same epoch-1 checkpoints where layers $1$--$4$ are essentially zero, layer $0$ has cosine $+0.42$, $+0.44$, and $+0.42$ across seeds (Table~\ref{tab:mode_validation}; per-seed values in Appendix~\ref{app:layer0_dominance}). The resulting average can therefore be driven by the embedding layer even when the interior blocks are effectively unaligned, so aggregate reporting obscures the very distinction needed to separate ``measurement collapse'' from ``poor credit direction.'' This layer-$0$ dominance is specific to the ResMLP DFA setting; on ViT-Mini DFA, all layers are near zero, which strengthens the broader methodological point that alignment should be reported per layer rather than only in aggregate. With the two modes separated observationally, the remaining question is whether intervention can move them independently.
 
-\paragraph{Per-layer reporting is mandatory: layer-0 dominance.} Per-layer reporting is therefore not cosmetic. In ResMLP under vanilla DFA, the headline aggregate alignment $\Gamma \approx 0.07$--$0.10$ can look mildly positive only because layer $0$ remains strongly aligned while the deep network is not: at the same epoch-1 checkpoints where layers $1$--$4$ are essentially zero, layer $0$ has cosine $+0.42$, $+0.44$, and $+0.42$ across seeds (Table~\ref{tab:mode_validation}; per-seed values in Appendix~\ref{app:layer0_dominance}). The resulting average can therefore be driven by the embedding layer even when the interior blocks are effectively unaligned, so aggregate reporting obscures the very distinction needed to separate ``measurement collapse'' from ``poor credit direction.'' This layer-$0$ dominance is specific to the ResMLP DFA setting; on ViT-Mini DFA, all layers are near zero, which strengthens the broader methodological point that alignment should be reported per layer rather than only in aggregate. With the two modes separated observationally, the remaining question is whether intervention can move them independently.
+\subsection{Functional triangulation}
 
-\paragraph{Method-dependent severity once Mode~1 is alleviated.} Mode~2 has method-dependent severity within the audited fixed-feedback family once Mode~1 is alleviated. Applying the same $\lambda{=}10^{-2}$ scale-control penalty to SB, CB, and DFA on the audited 4-block $d{=}256$ ResMLP for $30$ epochs (three seeds) gives, in order, test accuracies $0.453 \pm 0.003$, $0.360 \pm 0.004$, $0.360 \pm 0.002$ and deep mean cosines $+0.322 \pm 0.008$, $+0.679 \pm 0.010$, $+0.151 \pm 0.025$ (deep mean $\rho$ $+0.402$, $+0.464$, $+0.080$ and full $\|h_L\|/\|g_L\|$ in Appendix~\ref{app:sb_penalty}), all in the meaningful-measurement regime. SB+penalty is the first audited non-BP method whose trained deep blocks beat the frozen-blocks baseline ($0.349$), by $+10.4$ pp---comparable to BP+penalty's $+18.3$ pp.
+Within this rescued regime the three methods reveal a clean cosine-versus-accuracy dissociation, and two independent functional measurements rule out the interpretation that cosine is just noisy. \emph{Nudging:} a single step $\eta{=}0.01$ along each method's per-layer credit $a_l$ at the converged checkpoint changes the deep-block test loss by $-1.93 \pm 0.14 \times 10^{-3}$ (SB+pen), $-4.26 \pm 0.29 \times 10^{-4}$ (CB+pen), and $-4.98 \pm 0.53 \times 10^{-5}$ (DFA+pen) across three seeds (per-seed values in Appendix~\ref{app:sb_penalty}): SB moves the loss $\approx\!4.5\times$ more than CB and $\approx\!39\times$ more than DFA, even though CB has the highest deep cosine with BP. \emph{Training-loss trajectory:} the integrated 30-epoch training loss decrease across three seeds ranks SB ($-0.447 \pm 0.010$) $\gg$ CB ($-0.121 \pm 0.003$) $\approx$ DFA ($-0.095 \pm 0.008$). All three functional metrics (accuracy, nudging, training-loss trajectory) agree on SB $\gg$ CB $\approx$ DFA; the deep-cosine ordering CB $>$ SB $>$ DFA is the only one that disagrees (Figure~\ref{fig:cos_acc_dissoc}).
 
-\paragraph{Three functional metrics rank the methods consistently; cosine disagrees.} Within this rescued regime the three methods reveal a clean cosine-versus-accuracy dissociation, and two independent functional measurements rule out the interpretation that cosine is just noisy. \emph{Nudging:} a single step $\eta{=}0.01$ along each method's per-layer credit $a_l$ at the converged checkpoint changes the deep-block test loss by $-1.93 \pm 0.14 \times 10^{-3}$ (SB+pen), $-4.26 \pm 0.29 \times 10^{-4}$ (CB+pen), and $-4.98 \pm 0.53 \times 10^{-5}$ (DFA+pen) across three seeds (per-seed values in Appendix~\ref{app:sb_penalty}): SB moves the loss $\approx\!4.5\times$ more than CB and $\approx\!39\times$ more than DFA, even though CB has the highest deep cosine with BP. \emph{Training-loss trajectory:} the integrated 30-epoch training loss decrease across three seeds ranks SB ($-0.447 \pm 0.010$) $\gg$ CB ($-0.121 \pm 0.003$) $\approx$ DFA ($-0.095 \pm 0.008$). All three functional metrics (accuracy, nudging, training-loss trajectory) agree on SB $\gg$ CB $\approx$ DFA; the deep-cosine ordering CB $>$ SB $>$ DFA is the only one that disagrees (Figure~\ref{fig:cos_acc_dissoc}).
+We frame the Mode~2 reading as a three-part proposition. \emph{Observation}: under the same intervention and budget, CB has $4\times$ DFA's deep cosine yet matches DFA's accuracy, while SB attains the best accuracy with intermediate cosine; the same SB $\gg$ CB $\approx$ DFA ranking is reproduced by single-step nudging and 30-epoch training-loss decrease. \emph{Inference}: layerwise cosine is necessary to rule out grossly wrong credit signals---it cleanly distinguishes the rescued regime from the clamp-dominated vanilla regime where deep cos is essentially zero---but it is not sufficient to certify that the supplied signal is useful credit for depth, because three independent functional metrics rank the same three methods in the opposite order from cosine. \emph{Mechanism hypothesis}: usefulness depends on whether the local update induces useful forward-state change across blocks, not merely on the angle between the local credit direction and the BP gradient. Under this reading, CB supplies a gradient-direction surrogate that aligns in angle without translating into coordinated forward-state improvement, while SB supplies a state-level teaching signal that preserves aspects of useful credit which layerwise cosine does not measure. The single-step nudging test and the integrated training-loss decrease are direct functional probes of exactly this distinction: they measure what an actual descent step in the proposed credit direction does to the loss, rather than how the direction angle compares to the BP gradient at one frozen point.
 
-\paragraph{A three-part proposition: observation, inference, mechanism hypothesis.} We frame the Mode~2 reading as a three-part proposition. \emph{Observation}: under the same intervention and budget, CB has $4\times$ DFA's deep cosine yet matches DFA's accuracy, while SB attains the best accuracy with intermediate cosine; the same SB $\gg$ CB $\approx$ DFA ranking is reproduced by single-step nudging and 30-epoch training-loss decrease. \emph{Inference}: layerwise cosine is necessary to rule out grossly wrong credit signals---it cleanly distinguishes the rescued regime from the clamp-dominated vanilla regime where deep cos is essentially zero---but it is not sufficient to certify that the supplied signal is useful credit for depth, because three independent functional metrics rank the same three methods in the opposite order from cosine. \emph{Mechanism hypothesis}: usefulness depends on whether the local update induces useful forward-state change across blocks, not merely on the angle between the local credit direction and the BP gradient. Under this reading, CB supplies a gradient-direction surrogate that aligns in angle without translating into coordinated forward-state improvement, while SB supplies a state-level teaching signal that preserves aspects of useful credit which layerwise cosine does not measure. The single-step nudging test and the integrated training-loss decrease are direct functional probes of exactly this distinction: they measure what an actual descent step in the proposed credit direction does to the loss, rather than how the direction angle compares to the BP gradient at one frozen point.
+\subsection{From Mode~2 to Mode~1?}
 
-\paragraph{Mode~1 may be a downstream symptom of Mode~2.} The same mechanism story suggests a causal reading of the relationship between the two failure modes: that Mode~1 is plausibly a downstream symptom of Mode~2 rather than a parallel, independent failure. The reasoning is constructive. Each fixed-feedback method's local objective is the inner product $\langle f_l(h_l),\, a_l\rangle$, with no penalty on $\|f_l\|$. If the credit vector $a_l$ does not point along a direction in which a small change of the residual contribution $f_l$ produces useful forward-state improvement (Mode~2), then the only remaining way for the optimizer to keep increasing the inner product is to inflate $\|f_l\|$ in the direction set by the random $a_l$, since that is the cheap path for which the architecture supplies no global restraint. Inflating $\|f_l\|$ directly produces the activation-growth signature of Mode~1(a), and via the LN Jacobian relation $\|g_L\|=\Theta(1/\|h_L\|)$ derived in Section~\ref{sec:mode1} it then drives the gradient-floor collapse of Mode~1(b). The per-block penalty $\lambda \|f_l\|^2$ breaks this chain at the inflation step by adding an explicit cost to growing $\|f_l\|$, which contains $\|h_L\|$ and lifts $\|g_L\|$ above the diagnostic floor without ever modifying the underlying credit-direction quality of $a_l$. This explains the otherwise-asymmetric observation that the same intervention alleviates Mode~1 (a)+(b) cleanly while leaving Mode~2 only partially addressed: the penalty addresses the symptom, not the cause.
+The same mechanism story suggests a causal reading of the relationship between the two failure modes: that Mode~1 is plausibly a downstream symptom of Mode~2 rather than a parallel, independent failure. The reasoning is constructive. Each fixed-feedback method's local objective is the inner product $\langle f_l(h_l),\, a_l\rangle$, with no penalty on $\|f_l\|$. If the credit vector $a_l$ does not point along a direction in which a small change of the residual contribution $f_l$ produces useful forward-state improvement (Mode~2), then the only remaining way for the optimizer to keep increasing the inner product is to inflate $\|f_l\|$ in the direction set by the random $a_l$, since that is the cheap path for which the architecture supplies no global restraint. Inflating $\|f_l\|$ directly produces the activation-growth signature of Mode~1(a), and via the LN Jacobian relation $\|g_L\|=\Theta(1/\|h_L\|)$ derived in Section~\ref{sec:mode1} it then drives the gradient-floor collapse of Mode~1(b). The per-block penalty $\lambda \|f_l\|^2$ breaks this chain at the inflation step by adding an explicit cost to growing $\|f_l\|$, which contains $\|h_L\|$ and lifts $\|g_L\|$ above the diagnostic floor without ever modifying the underlying credit-direction quality of $a_l$. This explains the otherwise-asymmetric observation that the same intervention alleviates Mode~1 (a)+(b) cleanly while leaving Mode~2 only partially addressed: the penalty addresses the symptom, not the cause.
 
-\paragraph{Hypothesis status and reporting rule.} We state this as a hypothesis rather than a theorem for two reasons. First, we have measured the angle-to-accuracy gap and two functional proxies (nudging and training-loss decrease) but not the full per-block forward-state-change content over training. Second, the data is also formally consistent with a parallel-failure-mode reading in which Mode~1 and Mode~2 are independently destructive and the penalty happens to address Mode~1 only; nothing in the audit forces the downstream-of-Mode~2 reading over this alternative. The reporting rule that follows is robust to either interpretation: if Mode~1 is downstream then the penalty addresses a symptom and the lower-bound credit-quality gap is the dominant residual, while if the modes are parallel then the penalty addresses Mode~1 only and Mode~2 remains an additive deficit; in both cases the cross-method dissociation between deep cosine and the three functional metrics strengthens the methodological point that alignment must be reported jointly with measurement validity and a depth-utilization baseline rather than as a single headline number.
+We state this as a hypothesis rather than a theorem for two reasons. First, we have measured the angle-to-accuracy gap and two functional proxies (nudging and training-loss decrease) but not the full per-block forward-state-change content over training. Second, the data is also formally consistent with a parallel-failure-mode reading in which Mode~1 and Mode~2 are independently destructive and the penalty happens to address Mode~1 only; nothing in the audit forces the downstream-of-Mode~2 reading over this alternative. The reporting rule that follows is robust to either interpretation: if Mode~1 is downstream then the penalty addresses a symptom and the lower-bound credit-quality gap is the dominant residual, while if the modes are parallel then the penalty addresses Mode~1 only and Mode~2 remains an additive deficit; in both cases the cross-method dissociation between deep cosine and the three functional metrics strengthens the methodological point that alignment must be reported jointly with measurement validity and a depth-utilization baseline rather than as a single headline number.
 
 \begin{figure}[t]
 \centering
@@ -118,7 +134,11 @@ Credit Bridge & $0.289 \pm 0.031$ & $0.07$        & trustworthy & walked back \\
 \section{Intervention and Cross-Architecture Evidence}
 \label{sec:validation}
 
-\paragraph{The penalty rescues the measurement regime.} The penalty intervention first matters as a rescue of the measurement regime. When we add a per-block penalty $\lambda \,\mathrm{mean}(\|f_l(h_l)\|^2)$ to DFA's local loss and train the 4-block $d{=}256$ ResMLP for 30 epochs on CIFAR-10, the $\lambda{=}10^{-2}$ setting contains the terminal hidden-state scale from $\|h_L\| \sim 4.4\times 10^8$ under vanilla DFA to $\sim 4.0\times 10^4$, while lifting the deepest BP reference norm from $\|g_L\| \sim 5\times 10^{-10}$ to $\sim 9.0\times 10^{-7}$, a roughly four-order-of-magnitude rescue on both quantities (Figure~\ref{fig:penalty_rescue}; Table~\ref{tab:mode_validation}). At that setting, both diagnostic~(a) and diagnostic~(b) pass on penalized DFA, and test accuracy rises to $0.360 \pm 0.002$ from $0.301 \pm 0.006$ for matched 30-epoch vanilla DFA. The key point is not yet that the recovered network has good deep credit, but that the deep reference vector is again large enough to function as a meaningful target direction rather than a clamp-dominated artifact. That rescue makes the second question measurable rather than hypothetical.
+\subsection{Penalty rescue and sweep}
+
+Mode~2 has method-dependent severity within the audited fixed-feedback family once Mode~1 is alleviated. Applying the same $\lambda{=}10^{-2}$ scale-control penalty to SB, CB, and DFA on the audited 4-block $d{=}256$ ResMLP for $30$ epochs (three seeds) gives, in order, test accuracies $0.453 \pm 0.003$, $0.360 \pm 0.004$, $0.360 \pm 0.002$ and deep mean cosines $+0.322 \pm 0.008$, $+0.679 \pm 0.010$, $+0.151 \pm 0.025$ (deep mean $\rho$ $+0.402$, $+0.464$, $+0.080$ and full $\|h_L\|/\|g_L\|$ in Appendix~\ref{app:sb_penalty}), all in the meaningful-measurement regime. SB+penalty is the first audited non-BP method whose trained deep blocks beat the frozen-blocks baseline ($0.349$), by $+10.4$ pp---comparable to BP+penalty's $+18.3$ pp.
+
+The penalty intervention first matters as a rescue of the measurement regime. When we add a per-block penalty $\lambda \,\mathrm{mean}(\|f_l(h_l)\|^2)$ to DFA's local loss and train the 4-block $d{=}256$ ResMLP for 30 epochs on CIFAR-10, the $\lambda{=}10^{-2}$ setting contains the terminal hidden-state scale from $\|h_L\| \sim 4.4\times 10^8$ under vanilla DFA to $\sim 4.0\times 10^4$, while lifting the deepest BP reference norm from $\|g_L\| \sim 5\times 10^{-10}$ to $\sim 9.0\times 10^{-7}$, a roughly four-order-of-magnitude rescue on both quantities (Figure~\ref{fig:penalty_rescue}; Table~\ref{tab:mode_validation}). At that setting, both diagnostic~(a) and diagnostic~(b) pass on penalized DFA, and test accuracy rises to $0.360 \pm 0.002$ from $0.301 \pm 0.006$ for matched 30-epoch vanilla DFA. The key point is not yet that the recovered network has good deep credit, but that the deep reference vector is again large enough to function as a meaningful target direction rather than a clamp-dominated artifact. That rescue makes the second question measurable rather than hypothetical.
 
 \begin{table}[t]
 \centering
@@ -138,11 +158,13 @@ Fresh-$B$ null control & $\overline{\cos}_{deep}{=}+0.002{\pm}0.022$ ($n{=}20$ d
 \end{tabular}}
 \end{table}
 
-\paragraph{Penalty alleviates Mode~2 only partially; the $\lambda$ sweep separates the modes.} Once the reference vector is meaningful again, the deep layers no longer sit exactly at null. At $\lambda{=}10^{-2}$, penalized DFA reaches a three-seed deep-layer mean cosine of $+0.151 \pm 0.025$ and deep perturbation correlation of $+0.080 \pm 0.012$, whereas vanilla DFA is essentially zero on both metrics in the deep blocks, consistent with prior concerns that alternative feedback can fail by supplying poor credit directions even before full collapse \citep{bartunov2018assessing,moskovitz2018feedback,crafton2019backpropagation,refinetti2023aligning}. The null calibration rules out the interpretation that this recovered signal is merely measurement noise: on the same penalized checkpoint, replacing the training-time feedback matrices with 20 fresh random $B_l$ draws gives a deep cosine of only $+0.002 \pm 0.022$, with per-layer standard deviations of $0.013$--$0.023$, all within noise of zero (Table~\ref{tab:mode_validation}). The $\lambda$ sweep sharpens the dissociation further: at $\lambda{=}10^{-4}$, Mode~1 is already alleviated, with three-seed mean $\|h_L\|{\approx}2.2\times 10^4$ and $\|g_L\|{\approx}7.0\times 10^{-7}$, but the three-seed deep cosine remains $-0.020$, while $\lambda{=}10^{-2}$ delivers the $+0.151$ and $+0.080$ above (Figure~\ref{fig:penalty_rescue}). The improvement is real, but it is only partial.
+Once the reference vector is meaningful again, the deep layers no longer sit exactly at null. At $\lambda{=}10^{-2}$, penalized DFA reaches a three-seed deep-layer mean cosine of $+0.151 \pm 0.025$ and deep perturbation correlation of $+0.080 \pm 0.012$, whereas vanilla DFA is essentially zero on both metrics in the deep blocks, consistent with prior concerns that alternative feedback can fail by supplying poor credit directions even before full collapse \citep{bartunov2018assessing,moskovitz2018feedback,crafton2019backpropagation,refinetti2023aligning}. The null calibration rules out the interpretation that this recovered signal is merely measurement noise: on the same penalized checkpoint, replacing the training-time feedback matrices with 20 fresh random $B_l$ draws gives a deep cosine of only $+0.002 \pm 0.022$, with per-layer standard deviations of $0.013$--$0.023$, all within noise of zero (Table~\ref{tab:mode_validation}). The $\lambda$ sweep sharpens the dissociation further: at $\lambda{=}10^{-4}$, Mode~1 is already alleviated, with three-seed mean $\|h_L\|{\approx}2.2\times 10^4$ and $\|g_L\|{\approx}7.0\times 10^{-7}$, but the three-seed deep cosine remains $-0.020$, while $\lambda{=}10^{-2}$ delivers the $+0.151$ and $+0.080$ above (Figure~\ref{fig:penalty_rescue}). The improvement is real, but it is only partial.
 
-\paragraph{Capacity-cost control: BP under the same penalty.} A rescue intervention is only informative if its direct cost is controlled. The relevant control is BP trained under the same penalty for the same matched $30$-epoch budget: across three seeds, BP falls from $0.585 \pm 0.001$ without the penalty to $0.532 \pm 0.007$ with $\lambda{=}10^{-2}$, so the penalty has a direct cost of about $5.3$ percentage points even when credit assignment is correct, whereas DFA moves in the opposite direction, from $0.301 \pm 0.006$ to $0.360 \pm 0.002$, and State Bridge moves further still, from $0.213$ to $0.453 \pm 0.003$, all under the same $30$-epoch intervention (Figure~\ref{fig:penalty_rescue}; Appendix~\ref{app:sb_penalty}). Relative to the frozen-blocks baseline of $0.349$, BP+penalty retains a margin of $+18.3$ points, State Bridge+penalty retains $+10.4$ points, and DFA+penalty retains only $+1.1$ points. The remaining BP-to-DFA gap of $17.2$ points is therefore a lower bound on the part of DFA's deficit that is not explained by simple penalty-induced capacity loss alone, though not a clean isolation because BP uses an end-to-end loss whereas DFA uses block-local losses. The substantially smaller BP-to-State-Bridge gap of $0.532 - 0.453 = 7.9$ points shows that the cross-method differences in penalty-rescued accuracy are not all attributable to a uniform ``random-feedback ceiling'': the bridge construction in State Bridge can recover much more of the BP-with-penalty performance than DFA can, on the same architecture and the same intervention. The residual gap after that control is what keeps Mode~2 substantively alive while letting it have method-dependent severity.
+\subsection{Cost and transfer}
 
-\paragraph{Cross-architecture and depth-sweep evidence.} The architecture comparison sharpens the scope of the critique. In the terminal-LN architectures we audited, both diagnostics fire for DFA-trained ResMLP at $d{=}256$, the same pattern recurs at $d{=}512$ with even larger max-per-block growth (DFA three-seed mean about $7\times 10^3$ vs $\sim\!1.9\times 10^3$ at $d{=}256$), and ViT-Mini with a class token and terminal LN shows diagnostic~(a) by epoch~1 and diagnostic~(b) by epochs~2--3 (Figure~\ref{fig:temporal_cross_arch}). A depth sweep on the $d{=}512$ ResMLP at $L \in \{2,4,6,8,12\}$ shows that the layerwise pattern is essentially depth-invariant: DFA's layer-0 cosine stays in $[+0.38,+0.40]$ across all five depths, while its mean deep-layer cosine stays within $[-0.005,+0.000]$ and its deep perturbation correlation collapses to $0.000$ in every depth tested, even though BP retains a deep-layer cosine of $+0.94$ at $L{=}12$ (Appendix~\ref{app:depth_scan}). The deep credit signal does not improve when the network is shallower, so the failure is not a "too deep" artifact. In the non-terminal-LN controls, the pattern is different: the no-terminal-LN ResMLP-d256 ablation shows diagnostic~(a) firing across three seeds at epochs $\{18, 14, 25\}$ but diagnostic~(b) never fires across $100$ epochs and the same three seeds, and the BatchNorm CNN on CIFAR-10 likewise shows strong growth under DFA, with max-per-block growth up to $237\times$, but keeps deepest BP gradients around $\|g\| \sim 10^{-3}$ and never triggers diagnostic~(b) (Figure~\ref{fig:temporal_cross_arch}). BP never triggers either diagnostic in any audited architecture. The matched same-backbone ResMLP-d256 ablation in Section~\ref{sec:mode1} supplies the cleanest causal control: removing terminal LayerNorm from the same architecture preserves activation growth but eliminates the gradient floor, so diagnostic~(b) is necessary on terminal-LN ResMLP and is not just an architecture-class coincidence. The broader claim therefore holds at full strength inside the audited residual ResMLP and ViT-Mini regime, while diagnostic~(a) remains useful more broadly. This lets the paper end with a reporting rule rather than an overclaimed theory.
+A rescue intervention is only informative if its direct cost is controlled. The relevant control is BP trained under the same penalty for the same matched $30$-epoch budget: across three seeds, BP falls from $0.585 \pm 0.001$ without the penalty to $0.532 \pm 0.007$ with $\lambda{=}10^{-2}$, so the penalty has a direct cost of about $5.3$ percentage points even when credit assignment is correct, whereas DFA moves in the opposite direction, from $0.301 \pm 0.006$ to $0.360 \pm 0.002$, and State Bridge moves further still, from $0.213$ to $0.453 \pm 0.003$, all under the same $30$-epoch intervention (Figure~\ref{fig:penalty_rescue}; Appendix~\ref{app:sb_penalty}). Relative to the frozen-blocks baseline of $0.349$, BP+penalty retains a margin of $+18.3$ points, State Bridge+penalty retains $+10.4$ points, and DFA+penalty retains only $+1.1$ points. The remaining BP-to-DFA gap of $17.2$ points is therefore a lower bound on the part of DFA's deficit that is not explained by simple penalty-induced capacity loss alone, though not a clean isolation because BP uses an end-to-end loss whereas DFA uses block-local losses. The substantially smaller BP-to-State-Bridge gap of $0.532 - 0.453 = 7.9$ points shows that the cross-method differences in penalty-rescued accuracy are not all attributable to a uniform ``random-feedback ceiling'': the bridge construction in State Bridge can recover much more of the BP-with-penalty performance than DFA can, on the same architecture and the same intervention. The residual gap after that control is what keeps Mode~2 substantively alive while letting it have method-dependent severity.
+
+The architecture comparison sharpens the scope of the critique. In the terminal-LN architectures we audited, both diagnostics fire for DFA-trained ResMLP at $d{=}256$, the same pattern recurs at $d{=}512$ with even larger max-per-block growth (DFA three-seed mean about $7\times 10^3$ vs $\sim\!1.9\times 10^3$ at $d{=}256$), and ViT-Mini with a class token and terminal LN shows diagnostic~(a) by epoch~1 and diagnostic~(b) by epochs~2--3 (Figure~\ref{fig:temporal_cross_arch}). A depth sweep on the $d{=}512$ ResMLP at $L \in \{2,4,6,8,12\}$ shows that the layerwise pattern is essentially depth-invariant: DFA's layer-0 cosine stays in $[+0.38,+0.40]$ across all five depths, while its mean deep-layer cosine stays within $[-0.005,+0.000]$ and its deep perturbation correlation collapses to $0.000$ in every depth tested, even though BP retains a deep-layer cosine of $+0.94$ at $L{=}12$ (Appendix~\ref{app:depth_scan}). The deep credit signal does not improve when the network is shallower, so the failure is not a "too deep" artifact. In the non-terminal-LN controls, the pattern is different: the no-terminal-LN ResMLP-d256 ablation shows diagnostic~(a) firing across three seeds at epochs $\{18, 14, 25\}$ but diagnostic~(b) never fires across $100$ epochs and the same three seeds, and the BatchNorm CNN on CIFAR-10 likewise shows strong growth under DFA, with max-per-block growth up to $237\times$, but keeps deepest BP gradients around $\|g\| \sim 10^{-3}$ and never triggers diagnostic~(b) (Figure~\ref{fig:temporal_cross_arch}). BP never triggers either diagnostic in any audited architecture. The matched same-backbone ResMLP-d256 ablation in Section~\ref{sec:mode1} supplies the cleanest causal control: removing terminal LayerNorm from the same architecture preserves activation growth but eliminates the gradient floor, so diagnostic~(b) is necessary on terminal-LN ResMLP and is not just an architecture-class coincidence. The broader claim therefore holds at full strength inside the audited residual ResMLP and ViT-Mini regime, while diagnostic~(a) remains useful more broadly. This lets the paper end with a reporting rule rather than an overclaimed theory.
 
 \begin{figure}[t]
 \centering
@@ -168,7 +190,9 @@ Fresh-$B$ null control & $\overline{\cos}_{deep}{=}+0.002{\pm}0.022$ ($n{=}20$ d
 \section{Recommended FA Evaluation Protocol}
 \label{sec:protocol}
 
-\paragraph{Start from measurement validity.} The reporting protocol begins with measurement validity. Before any FA paper reports a headline alignment number, it should report per-layer state scale and the hidden BP reference-gradient scale at the layers where the scientific claim is being made. In our audited regime, those two quantities already separate healthy from invalid measurement with unusually wide margins: the maximum per-block growth stays below about $11\times$ for BP and EP but is at least $694\times$ for the degenerate methods, giving a $63\times$ calibration gap, while the deepest hidden BP norm stays above about $10^{-4}$ for BP and EP but below about $4\times 10^{-9}$ for the degenerate methods, giving a $24{,}338\times$ gap (Table~\ref{tab:protocol_def}; Table~\ref{tab:main_audit}; Figure~\ref{fig:cross_arch_summary}). These are not cosmetic diagnostics around the real result: they determine whether the reported cosine is being computed against an informative BP direction or against a floor-level reference. If the reference gradient is at floor, the evaluator should stop treating aggregate alignment as evidence.
+\subsection{Validity-first screening}
+
+The reporting protocol begins with measurement validity. Before any FA paper reports a headline alignment number, it should report per-layer state scale and the hidden BP reference-gradient scale at the layers where the scientific claim is being made. In our audited regime, those two quantities already separate healthy from invalid measurement with unusually wide margins: the maximum per-block growth stays below about $11\times$ for BP and EP but is at least $694\times$ for the degenerate methods, giving a $63\times$ calibration gap, while the deepest hidden BP norm stays above about $10^{-4}$ for BP and EP but below about $4\times 10^{-9}$ for the degenerate methods, giving a $24{,}338\times$ gap (Table~\ref{tab:protocol_def}; Table~\ref{tab:main_audit}; Figure~\ref{fig:cross_arch_summary}). These are not cosmetic diagnostics around the real result: they determine whether the reported cosine is being computed against an informative BP direction or against a floor-level reference. If the reference gradient is at floor, the evaluator should stop treating aggregate alignment as evidence.
 
 \begin{table}[t]
 \centering
@@ -188,16 +212,22 @@ Diag. & Measurement & Default threshold & Role \\
 \end{tabular}}
 \end{table}
 
-\paragraph{Decision value: which diagnostics actually walk back which methods.} The point of the protocol is not to add plots; it is to prevent a specific class of false conclusions. For this paper, the minimal protocol is four checks: per-layer activation scale via max-per-block growth, deepest hidden BP gradient floor, meaningful-regime per-layer credit quality, and an architecture-matched frozen-blocks baseline (Table~\ref{tab:protocol_def}). The first two ask whether the reference quantity is still valid; the third asks whether, once validity is restored, the deep blocks receive useful directions; and the fourth asks whether the trained depth is doing better than a model whose residual blocks were never trained at all. Figure~\ref{fig:decision_utility} (Appendix~\ref{app:all_validations}) makes the decision value explicit: accuracy alone walks back $0/5$ audited methods, accuracy plus headline $\Gamma$ still walks back $0/5$, and the full protocol walks back $3/5$ by flagging DFA, State Bridge, and Credit Bridge, with diagnostics (a), (b), and (d) each independently sufficient for binary detection on those failures. On our audit, these checks catch failures that accuracy plus aggregate alignment miss completely.
+The point of the protocol is not to add plots; it is to prevent a specific class of false conclusions. For this paper, the minimal protocol is four checks: per-layer activation scale via max-per-block growth, deepest hidden BP gradient floor, meaningful-regime per-layer credit quality, and an architecture-matched frozen-blocks baseline (Table~\ref{tab:protocol_def}). The first two ask whether the reference quantity is still valid; the third asks whether, once validity is restored, the deep blocks receive useful directions; and the fourth asks whether the trained depth is doing better than a model whose residual blocks were never trained at all. Figure~\ref{fig:decision_utility} (Appendix~\ref{app:all_validations}) makes the decision value explicit: accuracy alone walks back $0/5$ audited methods, accuracy plus headline $\Gamma$ still walks back $0/5$, and the full protocol walks back $3/5$ by flagging DFA, State Bridge, and Credit Bridge, with diagnostics (a), (b), and (d) each independently sufficient for binary detection on those failures. On our audit, these checks catch failures that accuracy plus aggregate alignment miss completely.
 
-\paragraph{Diagnostic roles and calibration.} The protocol is conservative in a specific sense: it preserves BP and EP as evidence-bearing controls and walks back only claims that fail measurement-validity or depth-utilization checks. Diagnostics (a) and (b) have sharp empirical calibration gaps in the audited regime (Appendix~\ref{app:threshold_sweep}), diagnostic (c) is a sub-mode discriminator computed as the mean pairwise cosine of the per-batch-averaged BP-grad direction at the chosen layer across $K{\geq}8$ disjoint $128$-sample minibatches (in our 5-method audit, healthy methods cluster near zero with all six BP/EP values in $[-0.04,+0.12]$, while drift-dominated cases reach high tails up to $+0.99$, and $5/9$ degenerate values exceed the $0.30$ default cutoff), and diagnostic (d) uses a deliberately weak $2$pp margin as a context check rather than a theorem about useful depth. The Section~\ref{sec:mode2} cross-method cosine-versus-accuracy dissociation reinforces the necessity of keeping all four diagnostics separate: Credit Bridge, State Bridge, and DFA differ by more than $4\times$ in deep-layer alignment under the same penalty rescue without tracking final accuracy in the same direction, so aligning an alternative credit rule with the BP gradient is not a substitute for checking depth utilization against a matched shallow baseline.
+\subsection{Diagnostic roles and calibration}
+
+The protocol is conservative in a specific sense: it preserves BP and EP as evidence-bearing controls and walks back only claims that fail measurement-validity or depth-utilization checks. Diagnostics (a) and (b) have sharp empirical calibration gaps in the audited regime (Appendix~\ref{app:threshold_sweep}), diagnostic (c) is a sub-mode discriminator computed as the mean pairwise cosine of the per-batch-averaged BP-grad direction at the chosen layer across $K{\geq}8$ disjoint $128$-sample minibatches (in our 5-method audit, healthy methods cluster near zero with all six BP/EP values in $[-0.04,+0.12]$, while drift-dominated cases reach high tails up to $+0.99$, and $5/9$ degenerate values exceed the $0.30$ default cutoff), and diagnostic (d) uses a deliberately weak $2$pp margin as a context check rather than a theorem about useful depth. The Section~\ref{sec:mode2} cross-method cosine-versus-accuracy dissociation reinforces the necessity of keeping all four diagnostics separate: Credit Bridge, State Bridge, and DFA differ by more than $4\times$ in deep-layer alignment under the same penalty rescue without tracking final accuracy in the same direction, so aligning an alternative credit rule with the BP gradient is not a substitute for checking depth utilization against a matched shallow baseline.
 
 \section{Discussion, Limits, Conclusion}
 \label{sec:discussion}
 
-\paragraph{Scope, limits, and reporting recommendation.} \looseness=-2 Our claim is about evidence, not impossibility: we show that current FA evaluation practice can misread what happened, not that FA cannot work in deep networks. DFA, SB, and CB all pass status-quo reporting (Table~\ref{tab:main_audit}) but fail the protocol's deep checks, and the Figure~\ref{fig:penalty_rescue} penalty partially rescues credit signal rather than validating headlines. Our strongest claim is scoped to $d{=}256/512$ pre-LayerNorm ResMLPs and ViT-Mini, where both Mode~1 diagnostics fire; the no-terminal-LN ResMLP ablation establishes terminal LayerNorm as causally necessary for diagnostic~(b) on residual ResMLP and (with the BatchNorm CNN) shows that activation growth can persist without gradient-floor collapse; the dataset is CIFAR-10; and the BP-plus-penalty comparison is a lower bound, not a full decomposition. In the evaluation-methodology line of \citet{jordan2020evaluating,obray2022evaluation,paleka2026pitfalls}, FA papers should report BP-reference validity, layerwise credit quality, and a frozen-blocks depth-utilization baseline as separate axes, not a single headline.
+\subsection{Scope and reporting recommendation}
+
+Our claim is about evidence, not impossibility: we show that current FA evaluation practice can misread what happened, not that FA cannot work in deep networks. DFA, SB, and CB all pass status-quo reporting (Table~\ref{tab:main_audit}) but fail the protocol's deep checks, and the Figure~\ref{fig:penalty_rescue} penalty partially rescues credit signal rather than validating headlines. Our strongest claim is scoped to $d{=}256/512$ pre-LayerNorm ResMLPs and ViT-Mini, where both Mode~1 diagnostics fire; the no-terminal-LN ResMLP ablation establishes terminal LayerNorm as causally necessary for diagnostic~(b) on residual ResMLP and (with the BatchNorm CNN) shows that activation growth can persist without gradient-floor collapse; the dataset is CIFAR-10; and the BP-plus-penalty comparison is a lower bound, not a full decomposition. In the evaluation-methodology line of \citet{jordan2020evaluating,obray2022evaluation,paleka2026pitfalls}, FA papers should report BP-reference validity, layerwise credit quality, and a frozen-blocks depth-utilization baseline as separate axes, not a single headline.
+
+\subsection{Open questions}
 
-\paragraph{Open questions and concrete next experiments.} The mechanism story in Section~\ref{sec:mode2} treats Mode~1 as a plausible downstream symptom of Mode~2 rather than a parallel, independently destructive failure, but the audit data is also formally consistent with a fully parallel reading. A direct test would measure per-block forward-state-change content along the training trajectory and check whether per-block decrease in test loss tracks per-block credit usefulness (e.g.\ nudging-test loss change) more tightly than it tracks per-block angular agreement with the BP gradient; a complementary test would substitute the random feedback $B_l$ with a high-quality credit signal (sparse, learned to predict the BP gradient, or weight-transport-restored \`a la \citet{akrout2019deep}) at fixed $\|f_l\|$ and check whether activation growth still appears, which would falsify the Mode~2~$\to$~Mode~1 reading by exhibiting Mode~1 in the absence of Mode~2. Beyond the mechanism question, a wider-scope replication would extend the same audit to additional datasets (CIFAR-100, Tiny-ImageNet) and architectures outside the residual ResMLP / ViT-Mini family, which would calibrate how broadly the protocol's binary detectors generalize past the audited regime. The reference implementation in Appendix~\ref{app:reference_impl} is intended to support such extensions at the level of training-recipe and architecture-class configuration so the audit pipeline itself does not need to be re-derived.
+The mechanism story in Section~\ref{sec:mode2} treats Mode~1 as a plausible downstream symptom of Mode~2 rather than a parallel, independently destructive failure, but the audit data is also formally consistent with a fully parallel reading. A direct test would measure per-block forward-state-change content along the training trajectory and check whether per-block decrease in test loss tracks per-block credit usefulness (e.g.\ nudging-test loss change) more tightly than it tracks per-block angular agreement with the BP gradient; a complementary test would substitute the random feedback $B_l$ with a high-quality credit signal (sparse, learned to predict the BP gradient, or weight-transport-restored \`a la \citet{akrout2019deep}) at fixed $\|f_l\|$ and check whether activation growth still appears, which would falsify the Mode~2~$\to$~Mode~1 reading by exhibiting Mode~1 in the absence of Mode~2. Beyond the mechanism question, a wider-scope replication would extend the same audit to additional datasets (CIFAR-100, Tiny-ImageNet) and architectures outside the residual ResMLP / ViT-Mini family, which would calibrate how broadly the protocol's binary detectors generalize past the audited regime. The reference implementation in Appendix~\ref{app:reference_impl} is intended to support such extensions at the level of training-recipe and architecture-class configuration so the audit pipeline itself does not need to be re-derived.
 
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